Types of studies

We will include randomised controlled trials (RCTs), including those with an open‐label design. We will include reports of studies whether published or unpublished, except those published after 2010 for which we cannot access a registered protocol, in accordance with the policy of the Cochrane Injuries Group (Roberts 2015). We will not include cross‐over studies because we will be considering long‐term outcomes. Cluster‐randomised studies are unlikely to have been performed on this topic and will not be included.

Types of participants

We will include people aged 18 years and older with clinically diagnosed brain injury of unambiguously traumatic cause. We will include all severities of head injury: mild, moderate, or severe (according to the Glasgow Coma Score (GCS)) (Brain Trauma 2007). This includes any brain injury of traumatic aetiology that causes disturbance of consciousness and dysfunctions within six months of the initial trauma.

For trials including a subset of participants meeting our inclusion criteria (e.g. if a trial includes participants with other aetiology of brain injuries, such as secondary to hypoxia or cerebrovascular disease), we will attempt to use only the outcome data for the traumatic subset of participants by contacting the authors for this information. If for whatever reason these data are not available, we will only include the study in the review if the proportion of TBI participants is above 50%, with the ratio of TBI to other participants included in the 'Characteristics of included studies' table for each study. If we are unable to obtain the disaggregated data and the proportion of TBI participants remains unclear, we will include the study in the review but leave the data out of the meta‐analyses.

Types of interventions

We will include trials assessing the following comparisons.

1. Any DA agonist versus placebo

2. Any DA agonist plus usual care versus usual care alone

We will check to ensure that usual care, including non‐pharmacological rehabilitative therapy, was provided equally to people in both arms of all included studies.

Types of outcome measures

Electronic searches

The Cochrane Injuries Group's Information Specialist will conduct searches in the following databases for RCTs and controlled clinical trials. There will be no language or publication year restrictions.

1. Cochrane Central Register of Controlled Trials (which contains the Cochrane Injuries Trials Register) in the Cochrane Library (latest issue)

2. Ovid MEDLINE(R), Ovid MEDLINE(R) In‐Process & Other Non‐Indexed Citations, Ovid MEDLINE(R) Daily and Ovid OLDMEDLINE(R) (1946 to present)

3. Embase Classic + Embase (OvidSP) (1947 to present)

4. ISI Web of Science: Science Citation Index Expanded (SCI‐EXPANDED) (1970 to present)

5. ISI Web of Science: Conference Proceedings Citation Index‐Science (CPCI‐S) (1990 to present)

6. ClinicalTrials.gov (www.clinicaltrials.gov)

7. World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (apps.who.int/trialsearch)

The Information Specialist will adapt the MEDLINE search strategy illustrated in Appendix 1 as necessary for the other databases, including the RCT filter, which is a modified version of the Cochrane Highly Sensitive Search Strategies (Lefebvre 2011).

Searching other resources

We will search the reference lists of all included studies and reviews.

Selection of studies

Two review authors (NRP and SL) will independently screen the titles, abstracts, and keywords of citations obtained from the search of the electronic databases and exclude studies that do not fulfil the inclusion criteria. We will obtain full‐text reports of potentially eligible studies and studies for which the abstract provided insufficient information to determine eligibility. Two review authors will screen the full‐text reports for inclusion in the review. Any disagreements will be resolved by discussion, or through discussion with a third review author (CM) where necessary. We will examine all included studies to verify that they present unique datasets. If individual trials are reported in multiple papers, results will be assembled by trial ID and maximal data extracted. Duplicate results will be excluded if this is not possible.

We will record reasons for the exclusion of any study assessed at the full‐text stage and report key excluded studies in a 'Characteristics of excluded studies' table. We will agree on a hierarchy of reasons for study exclusion based on the inclusion criteria and will record the reason for exclusion as the first criterion not met. We will identify and exclude duplicates, and collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review.

Data extraction and management

Two review authors (NRP and SL) will independently extract data from the included studies and record the information on a data collection form. We will extract the following data.

1. General information about the article including authors and year of publication.

2. Methods: study design, total duration of study, study location, study setting, date of study, methods of statistical analysis.

3. Participants: age, gender, severity of TBI, diagnostic criteria if applicable, inclusion and exclusion criteria, similarity of groups at baseline, withdrawals.

4. Interventions: description of intervention, comparison, duration, route of administration, with or without other combined non‐standard treatment.

5. Outcomes: description of primary and secondary outcomes specified and collected, and time points reported.

6. Information relevant to 'Risk of bias' assessments including sequence generation, allocation concealment, loss to follow‐up, blinding of personnel, participants, and outcome assessors, and the likelihood of selective outcome reporting.

7. Notes: funding for the trial, details of ethical committee approval, details of prospective study registration, and notable conflicts of interest of trial authors.

We will request unpublished information from the study authors where necessary. Data extraction by each review author will be compared and any disagreements resolved through discussion or arbitration with a third review author (CM).

Assessment of risk of bias in included studies

Two review authors (NRP and SL) will independently assess the risk of bias of included studies using the 'Risk of bias' assessment tool described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will evaluate the risk of bias by assessing the following.

• Random sequence generation (checking for possible selection bias). We plan to assess the method used to generate the allocation sequence as: low risk of bias (any truly random process, e.g. random number table; computer random number generator); unclear risk of bias (method used to generate sequence not clearly stated). We will exclude studies using a non‐random process (e.g. odd or even date of birth; hospital or clinic record number).

• Allocation concealment (checking for possible selection bias). The method used to conceal allocation to interventions prior to assignment determines whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We will assess the methods as: low risk of bias (e.g. telephone or central randomisation; consecutively numbered, sealed, opaque envelopes); unclear risk of bias (method not clearly stated). We will exclude studies that did not conceal allocation (e.g. open list).

• Blinding of participants and personnel (checking for possible performance bias). We will assess the methods used to blind study participants and personnel from knowledge of which intervention a participant received. We will assess methods as: low risk of bias (study states that it was blinded and describes the method used to achieve blinding, such as identical tablets matched in appearance or smell, or a double‐dummy technique); unclear risk of bias (study states that it was blinded but does not provide an adequate description of how this was achieved). We will consider studies that are not double‐blind to be at high risk of bias.

• Blinding of outcome assessment (checking for possible detection bias). We aim to assess the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We will assess the methods as: low risk of bias (study has a clear statement that outcome assessors were unaware of treatment allocation, and ideally describes how this was achieved); unclear risk of bias (study states that outcome assessors were blind to treatment allocation but lacks a clear statement on how this was achieved). We will consider studies where outcome assessment was not blinded as being at high risk of bias.

• Selective reporting (checking for reporting bias). We will assess whether primary and secondary outcome measures were prespecified and whether these were consistent with those reported. We will assess selective reporting as: low risk of bias (studies reporting primary and secondary outcomes); high risk of bias (not all prespecified outcomes were reported or were only reported for certain data collection time points).

• Incomplete outcome data (checking for possible attrition bias due to the amount, nature, and handling of incomplete outcome data). We aim to assess the methods used to deal with incomplete data as: low risk (< 10% of participants did not complete the study and/or ‘baseline observation carried forward’ analysis was used); unclear risk of bias ('last observation carried forward' analysis was used); high risk of bias ('completer' analysis was used).

We will create a 'Risk of bias' table including our judgement of 'low risk', 'high risk', or 'unclear risk' of bias for each trial for each domain. The two review authors will resolve any disagreements through discussion or through arbitration involving a third review author. For each study we will provide summary statements to support our judgement, and where possible we will provide a quote from the study as further justification. We will summarise risk of bias across all studies for each type of bias.

Measures of treatment effect

We will pool outcomes by scales used, based on specific neuropsychiatric outcome measurements. Where possible, we will make comparisons between scales used (e.g. between alternative measures of functional recovery). Most scores are likely to be final outcomes, but some may be changes from baseline (e.g. GCS); we will handle these as separate analyses.

We will conduct analyses using data adjusted for baseline as opposed to unadjusted analyses. We will conduct an intention‐to‐treat analysis, as opposed to a per‐protocol analysis.

We will calculate the pooled risk ratio (RR) and 95% confidence interval (CI) for dichotomous data. For continuous data, we will use pooled mean difference (MD), or, where outcome data are reported on different scales that measure similar concepts, we will use standardised pooled mean difference (SMD) and 95% CI, back transforming the SMD to a familiar scale selected from a study included in the original meta‐analysis that is representative of the population and intervention and is at low risk of bias.

We will pool findings for the two primary outcomes and for the secondary outcomes of post‐traumatic amnesia and adverse events and side effects, where similar events are reported. For the remaining secondary outcomes of cognitive functioning and cognitive impairment, we will not pool data, as neuropsychiatric tests are validated for specific functions that are not open to generalisation.

Unit of analysis issues

The unit of analysis will be the individual participant.

For studies with multiple treatment groups, in the primary analysis we will combine results across all eligible interventions and compare them with the combined results across all eligible control groups, making single, pair‐wise comparisons. We will do this only if interventions are considered sufficiently similar. Where interventions are not considered sufficiently similar to combine, we will analyse each 'arm' of the trial separately (against a common control group), but divide the sample size for common comparator groups proportionately across each comparison (Higgins 2008). This simple approach will allow use of standard software (including Review Manager 5) (RevMan 2014), and prevent inappropriate double‐counting of participants.

Dealing with missing data

If data are missing from published reports, we will attempt to contact study authors to obtain this information. In the case of missing outcome data, we will only analyse the data that are available in the publication (i.e. we will not impute further). We will consider the potential impact of the missing data during the interpretation of the results.

Assessment of heterogeneity

We will examine statistical heterogeneity with visual inspection of the forest plot and taking into consideration the magnitude and direction of effect, as well as the I² statistic and Chi² test. We will consider substantial heterogeneity to exist with I² values greater than 80% and Chi² test P values less than 0.1. If there is substantial heterogeneity, we will assess heterogeneity by careful examination of the study reports and by using the preplanned subgroup analyses. We will consider whether it is appropriate to do a meta‐analysis, particularly if the direction of effect is inconsistent.

Assessment of reporting biases

To investigate the possibility of reporting biases, including publication bias, we will draw funnel plots (Egger 1997). Any asymmetry present might be due to publication bias, but might also be caused by a genuine relationship between trial size and effect size. We will examine clinical variation of the studies to explore asymmetry and will also compare results extracted from published journal reports with results obtained from other sources (e.g. trial protocols). We will only produce funnel plots if there is a minimum of 10 studies in any meta‐analysis.

Data synthesis

We will calculate the pooled RRs and 95% CIs for dichotomous outcomes, and the pooled MDs or SMD and 95% CIs for continuous outcomes using a random‐effects model. We have chosen a random‐effects model as we assume that there will be clinical and methodological differences between the included studies. We will test these assumptions by undertaking sensitivity analyses using a fixed‐effect model.

When using change from baseline score, we will follow the advice of the Cochrane Handbook for Systematic Reviews of Interventions in producing a meta‐analysis of mean differences (Deeks 2011). We will perform all analyses using Review Manager 5 (RevMan 2014). We will perform meta‐analysis if two or more studies assess the same outcome. If meta‐analysis is not possible, we will report study findings narratively.

Subgroup analysis and investigation of heterogeneity

Where there are sufficient data, we intend to perform the following subgroup analyses to account for clinical heterogeneity.

1. Severity of brain injury: severe TBI (GCS ≦ 8) versus moderate TBI (GCS 9 to 12) versus mild TBI (GCS 13 to 15).

2. Type of DA agonist (direct or indirectly acting), or individual drug if sufficient trials (at least three) are available.

3. Dose of DA agonist (high versus low, for specific drug).

4. Length of treatment: from one month but less than three months (short term); three months but less than six months (medium term); six months or longer (long term).

Sensitivity analysis

We will conduct sensitivity analyses to quantify differential effects (if any) when trials that we have assessed as at high risk of bias (with regard to the methods used to generate and conceal the randomisation sequence) are excluded. We will use Trial Sequential Analysis methods to explore any statistically significant effect found where the outcome did not meet the expected sample size.